Hydroxychloroquine in Nonhospitalized Adults With Early COVID-19
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Correction: Hydroxychloroquine in Nonhospitalized Adults With Early COVID-19FREE
There is no known effective oral therapy for early COVID-19. This randomized, double-blind, placebo-controlled trial evaluated effects of oral hydroxychloroquine on symptoms and disease severity in adult outpatients with early COVID-19.
Abstract
Background:
No effective oral therapy exists for early coronavirus disease 2019 (COVID-19).
Objective:
To investigate whether hydroxychloroquine could reduce COVID-19 severity in adult outpatients.
Design:
Randomized, double-blind, placebo-controlled trial conducted from 22 March through 20 May 2020. (ClinicalTrials.gov: NCT04308668)
Setting:
Internet-based trial across the United States and Canada (40 states and 3 provinces).
Participants:
Symptomatic, nonhospitalized adults with laboratory-confirmed COVID-19 or probable COVID-19 and high-risk exposure within 4 days of symptom onset.
Intervention:
Oral hydroxychloroquine (800 mg once, followed by 600 mg in 6 to 8 hours, then 600 mg daily for 4 more days) or masked placebo.
Measurements:
Symptoms and severity at baseline and then at days 3, 5, 10, and 14 using a 10-point visual analogue scale. The primary end point was change in overall symptom severity over 14 days.
Results:
Of 491 patients randomly assigned to a group, 423 contributed primary end point data. Of these, 341 (81%) had laboratory-confirmed infection with severe acute respiratory syndrome coronavirus 2 (SARS-CoV-2) or epidemiologically linked exposure to a person with laboratory-confirmed infection; 56% (236 of 423) were enrolled within 1 day of symptoms starting. Change in symptom severity over 14 days did not differ between the hydroxychloroquine and placebo groups (difference in symptom severity: relative, 12%; absolute, −0.27 point [95% CI, −0.61 to 0.07 point]; P = 0.117). At 14 days, 24% (49 of 201) of participants receiving hydroxychloroquine had ongoing symptoms compared with 30% (59 of 194) receiving placebo (P = 0.21). Medication adverse effects occurred in 43% (92 of 212) of participants receiving hydroxychloroquine versus 22% (46 of 211) receiving placebo (P < 0.001). With placebo, 10 hospitalizations occurred (2 non–COVID-19–related), including 1 hospitalized death. With hydroxychloroquine, 4 hospitalizations occurred plus 1 nonhospitalized death (P = 0.29).
Limitation:
Only 58% of participants received SARS-CoV-2 testing because of severe U.S. testing shortages.
Conclusion:
Hydroxychloroquine did not substantially reduce symptom severity in outpatients with early, mild COVID-19.
Primary Funding Source:
Private donors.
No effective oral therapy exists for the outpatient treatment of coronavirus disease 2019 (COVID-19). Reducing symptom severity and decreasing hospitalizations for outpatients is an important public health mitigation strategy for overcoming this pandemic. Hydroxychloroquine has in vitro activity against severe acute respiratory syndrome coronavirus 2 (SARS-CoV-2) and has been proposed as a potentially effective treatment (1).
Most clinical studies investigating therapies for COVID-19 have examined hospitalized patients with moderate to severe disease. The initial hydroxychloroquine studies were small and had methodological limitations, such as the absence of a control group (2, 3). Among large, nonrandomized, observational studies and clinical trials, emerging evidence suggests that antiviral therapy late in the course of COVID-19 may have, at best, minimal benefit (4–6). However, this therapy may have clinical benefits in the treatment of mild or moderate disease when given early in the disease course. To our knowledge, no randomized clinical trials to date have investigated agents for early COVID-19 in nonhospitalized patients.
We hypothesized that starting hydroxychloroquine therapy within the first few days of symptoms could alter the course of COVID-19 by reducing symptom severity and duration and preventing hospitalizations.
Methods
Design Overview
We conducted a multisite, international, randomized, double-blind, placebo-controlled trial with a parallel design (ClinicalTrials.gov: NCT04308668) (7). Because therapy is most likely to be effective if given early in the disease course, we sought to enroll persons as soon as possible after symptom onset; however, several challenges existed. First, in the United States during March and April 2020, SARS-CoV-2 diagnostic testing was extremely limited, nonhospitalized persons were often ineligible for testing, and turnaround time for results was multiple days. Second, SARS-CoV-2 can be undetectable when symptoms begin: The median false-negative rate of polymerase chain reaction (PCR) testing has been reported to be 38% on day 1 of symptoms (range, 18% to 65%), decreasing over subsequent days (8, 9). To overcome these challenges and initiate therapy as early as possible, we enrolled persons with either laboratory-confirmed COVID-19 or COVID-19–compatible symptoms and an epidemiologic link to a contact with laboratory-confirmed COVID-19. Participants were randomly assigned 1:1 to receive hydroxychloroquine or placebo. Recruitment began on 22 March 2020, enrollment stopped on 6 May, follow-up concluded on 20 May, and final hospital outcomes were known by 15 June 2020.
This study was approved by the University of Minnesota Institutional Review Board and conducted under an investigational new drug application (number 148257) from the U.S. Food and Drug Administration. In Canada, the study was conducted without objection from Health Canada (control number 237355), and ethics approval was obtained for each province separately from the Research Institute of the McGill University Health Centre, University of Manitoba, and University of Alberta.
Setting and Participants
We enrolled participants through internet-based surveys throughout the United States and the Canadian provinces of Quebec, Manitoba, and Alberta. Outreach for the trial was via traditional and social media. Participants completed a self-screening survey to determine eligibility. If eligible, after reading the consent form, participants answered a series of multiple-choice questions to assess study comprehension. Participants provided a digitally captured signature to document informed consent.
We enrolled nonhospitalized adults who were required to have 4 or fewer days of symptoms and either PCR-confirmed SARS-CoV-2 infection or compatible symptoms after a high-risk exposure to a person with PCR-confirmed COVID-19 within the past 14 days. High-risk exposure was defined as an immediate household contact or a close occupational exposure to someone with COVID-19 (for example, health care worker or first responder). Health care workers who had COVID-19–compatible symptoms and high-risk exposure but whose contact had PCR results pending were enrolled after symptom review by an infectious diseases physician. All of these participants met the COVID-19 case definition of the U.S. Council of State and Territorial Epidemiologists (Supplement) (10). Participants were excluded if they were younger than 18 years, were hospitalized, received certain medications, or met other safety exclusion criteria (Supplement).
Participants in a third group had a high-risk exposure and were asymptomatic at the time of consent for a companion postexposure prophylaxis trial, which had the same inclusion and exclusion criteria (11); however, these participants became symptomatic before starting their study medicine on day 1 and were analyzed as part of this trial.
Randomization and Interventions
Research pharmacists dispensed masked, 200-mg tablets of hydroxychloroquine sulfate or masked placebo. Allocation assignment was concealed from investigators and participants because the study medicine and placebo were similar in appearance: Both were white oblong tablets dispensed in opaque bottles. Study medication was shipped overnight to participants by commercial courier. Hydroxychloroquine was prescribed at 800 mg (4 tablets) once, then 600 mg (3 tablets) 6 to 8 hours later, then 600 mg (3 tablets) once daily for 4 more days (5 days in total). This dose was chosen on the basis of simulations that used previously published pharmacokinetic parameters and were designed to rapidly achieve and maintain a hydroxychloroquine concentration above the estimated half-maximal effective concentration (EC50) for SARS-CoV-2 (12). Simulations estimated that 94% of participants would achieve concentrations above this EC50 value on day 1 and that concentrations would be maintained for 10 to 14 days. Placebo tablets of folic acid, 400 mcg, were prescribed as an identical regimen for the control group. In Canada, the placebo tablets were lactose. If gastrointestinal upset occurred, we advised dividing the total daily dose into 2 or 3 doses.
Sequential randomization occurred at research pharmacies in Minneapolis, Minnesota, and Montreal, Canada. The trial statistician generated a permuted block randomization sequence using differently sized blocks in a 1:1 allocation, stratified by country. A separate randomization stratum also existed for persons who were initially asymptomatic at the time of informed consent but became symptomatic before receiving the study medication on day 1. The research pharmacies held this list, and statisticians verified that the randomization sequence was followed.
Outcomes and Follow-up
We collected self-reported survey data using the Research Electronic Data Capture (REDCap) system (13). We e-mailed participants follow-up surveys on days 1 (medication start date), 3, 5 (medication stop date), 10, and 14 to assess study medication adherence, adverse effects, presence and severity of COVID-19 symptoms, COVID-19 test results, and hospitalization status. If participants were hospitalized within 14 days, we continued follow-up past study completion to assess outcomes. We assessed symptom severity on a 10-point visual analogue scale, where 0 indicated no symptoms and 10 indicated severe symptoms (Supplement). Medication-related adverse events were collected with directed questioning on the most common adverse effects and an open-ended free-text field. For participants who did not respond to follow-up surveys, investigators used text messages, e-mails, or telephone calls to ascertain outcomes from them or their designated third-party contacts. If this was unsuccessful, investigators searched the internet for obituaries or other evidence of vital status.
Study End Points
The initial primary outcome was an ordinal outcome by day 14 of not hospitalized, hospitalized, or intensive care unit stay or death. Secondary end points were symptom severity at day 5 and day 14 by 10-point visual analogue scale, nominal incidence of all hospitalizations and deaths, and incidence of study medicine withdrawal.
Changes in End Point and Sample Sizes
Before the first interim analysis on 24 April 2020, it became apparent that the pooled event rate of hospitalization or death was substantially lower than our initial 10% expectation (original sample size calculations as described in Statistical Analysis section). Without unblinding of treatment allocation or analysis of the data, the principal investigator proposed to the data and safety monitoring board (DSMB) that we modify the primary end point to the change in overall symptom severity over 14 days as longitudinally measured on a 10-point visual analogue scale. The DSMB approved the change on 24 April 2020. The change was necessary because the low event rate of hospitalizations or deaths in the trial would have required increasing the sample size to 6000 participants, which was not attainable. With enrollment of at least 200 participants per group, we determined that the revised trial would have 90% power (with a 2-sided α level of 0.05) to detect a statistically significant difference between the groups for a change in symptom severity score as small as 0.25 point on the 10-point visual analogue scale. The trial halted at the second DSMB meeting on 6 May 2020, when the DSMB determined that sufficient statistical power had been achieved to evaluate the primary outcome.
Statistical Analysis
We had originally designed the trial assuming an 8% incidence of hospitalization and 2% incidence of intensive care unit stay or death (10% in total for these adverse outcomes) (14, 15). Using a proportional odds model with an estimated 50% effect size to reduce these ordinal outcomes with a 2-sided α level of 0.05 and 90% power, we had estimated 621 participants per group. With a novel internet-based trial, we had assumed that loss to follow-up might be higher than in a traditional trial; therefore, we had adjusted the sample size by 20% to 750 participants per group.
The primary analysis cohort included participants who completed at least 1 follow-up survey, so that change in symptom severity score could be assessed. The symptom severity score was self-assessed using a 10-point visual analogue scale (0 to 10, with 0.1-point increments). We assigned a severity score of 0 to those with no symptoms. Those who died of complications related to COVID-19 were assigned a severity score of 10 for any surveys missed up until the date of death. Both actual severity scores and changes in score from baseline were assessed for normality (Supplement Figure 4). We used a longitudinal mixed model, adjusted for baseline severity score, to analyze the primary end point of change in symptom severity through day 14. The absolute difference and 95% CI for change in severity score from baseline between groups are presented, along with the relative difference, calculated as [(hydroxychloroquine mean − placebo mean) / placebo mean]. A priori–specified subgroups for the primary outcome included days of symptoms before enrollment, age, sex, and laboratory-confirmed infection versus probable COVID-19. The primary end point was additionally assessed by medication adherence, zinc use, or vitamin C use as post hoc analyses. The Supplement gives additional detail on statistical methods and sensitivity analyses.
Analysis of the ordinal secondary end point of no hospitalization, hospitalization, or admission to the intensive care unit or death was not done because of the low event rate. The overall incidence of hospitalization or death was compared between the groups with Fisher exact tests. The analysis cohort for the outcome of hospitalization or death included all randomly assigned participants with vital status known at any point during follow-up. The presence of symptoms at each time point was assessed with the Fisher exact test, and we analyzed change from baseline symptom severity score at each visit using linear regression, adjusted for baseline severity score. We did analyses with SAS software, version 9.4 (SAS Institute), according to the intention-to-treat principle (that is, all participants with data are included in the analyses regardless of their medication status) with a 2-sided type I error using an α of 0.05. No adjustments for type I error were made to account for the number of secondary and subgroup analyses; therefore, subgroup analyses should be interpreted with caution.
Role of the Funding Source
The funders did not contribute to design, collection, management, analysis, interpretation of data, writing of the report, or the decision to submit the report for publication.
Results
We enrolled 491 participants from the United States and Canada (Figure 1), of whom 423 completed at least 1 follow-up survey with symptom data (to contribute data to the primary end point) and 465 contributed vital status data after enrollment (to contribute to the secondary end point of hospitalization or death). Twenty-six participants (5.3%) contributed no data after enrollment and are not included in any analyses. Of the 423 participants contributing data for the primary end point, there were 241 (57%) health care workers, 106 (25%) household contacts, and 76 (18%) with other exposures (Table). The median age was 40 years (interquartile range [IQR], 32 to 50 years), and 56% (n = 238) were women. Persons identifying as Black or African American were underrepresented (3%). Frequent comorbid conditions included asthma (11%), hypertension (11%), and diabetes (4%); 68% of participants reported no chronic medical conditions.
Eligible participants were allocated in a 1:1 ratio to receive masked placebo or hydroxychloroquine, 800 mg (4 tablets) once, then 600 mg (3 tablets) in 6–8 h, then 600 mg (3 tablets) daily for 4 more days. Persons who were exposed to a contact with a positive result on a polymerase chain reaction (PCR) test and who remained asymptomatic (n = 821) were enrolled in our companion trial on postexposure prophylaxis (11); however, 100 persons became symptomatic before receiving study medicine on day 1 and were included in this early treatment trial, as per the protocol-specified plan. Of these, 81 met the U.S. coronavirus disease 2019 (COVID-19) case definition on day 1 on the basis of their symptom complex, whereas 19 were possible COVID-19 on day 1 (10). Most of the 2237 symptomatic persons who were ineligible had >4 d of symptoms (55%) or did not have access to PCR testing (41%). PrEP = preexposure prophylaxis.
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Overall, 341 participants (81%) ultimately had either a positive PCR result or a high-risk exposure to a PCR-positive contact (Figure 2). Of these 341 persons, 145 were PCR-positive for SARS-CoV-2 and 280 had known high-risk exposure to a PCR-positive contact; 84 had both. The remaining 82 participants (19%) were enrolled with suspected COVID-19: They had COVID-19–compatible symptoms and reported high-risk exposure, but the contact's PCR was pending or unavailable. Of these, 37 had 2 of 3 symptoms of cough, fever, and shortness of breath. Those with a PCR-confirmed diagnosis took a mean of 2.2 days of symptoms to enroll, compared with 1.3 days for those enrolled via symptoms and an epidemiologic link to a PCR-positive contact (Supplement Table 7).
Venn diagram showing the distribution of how 378 participants qualified for enrollment. Two of 3 major symptoms were from among cough, shortness of breath, and fever. An additional 26 participants qualified by having pending (or unavailable) PCR tests at entry, having symptoms compatible with coronavirus disease 2019 (COVID-19), and meeting the case definition after adjudication by an infectious disease physician (10). Five persons later reported PCR-positive contact, with test results returning after enrollment. In addition, 19 initially asymptomatic persons who had been randomly assigned in the postexposure prophylaxis trial (11) developed new symptoms on day 1 but not 2 of 3 major symptoms. Figure 5 shows hierarchical outcomes by confirmed PCR positive, contact PCR positive, or probable case only. PCR = polymerase chain reaction.
At enrollment, 413 participants (98%) reported at least 1 COVID-19–compatible symptom; cough (65%), fatigue (52%), and headache (51%) were the most prevalent. Baseline symptoms were similar between study groups, and the median number of COVID-19–compatible symptoms reported was 4 (IQR, 2 to 6 symptoms). Overall, 56% (236 of 423) of participants enrolled within 1 day of symptom onset (Table).
We assessed the prevalence and severity of symptoms at each survey time point. By the fifth day, 54% (109 of 203) of participants receiving hydroxychloroquine reported symptoms, compared with 56% (108 of 194) receiving placebo. At day 14 of the trial, 24% (49 of 201) receiving hydroxychloroquine reported symptoms versus 30% (59 of 194) receiving placebo (P = 0.21) (Figure 3). These findings remained true when the comparisons were limited to symptoms of fever, cough, or shortness of breath at day 14 (16% receiving hydroxychloroquine vs. 22% receiving placebo).
The percentage of participants reporting symptoms over time did not statistically differ by use of hydroxychloroquine or placebo. By day 14, the proportion of hydroxychloroquine participants with symptoms was 6 percentage points less than that of placebo participants (24% vs. 30%; P = 0.21). The stacked bar graph distinguishes the relative proportions of those with presentation of cough, fever, or shortness of breath vs. other COVID-19–related symptoms. Exact percentages can be found in Supplement Figure 2. COVID-19 = coronavirus disease 2019.
For the primary outcome, we assessed the change in symptom severity score over 14 days in those given hydroxychloroquine versus placebo for 423 participants with available longitudinal data on symptom severity. The hydroxychloroquine group had a mean reduction from baseline of 2.60 points on the 10-point visual analogue scale for symptom severity, compared with a 2.33-point reduction in the placebo group (absolute difference, −0.27 point [95% CI, −0.61 to 0.07 point]; P = 0.117) (Figure 4). This equates to a non–statistically significant difference in average improvement in symptom severity of 12% between the hydroxychloroquine and placebo groups. Overall, hydroxychloroquine failed to cause a statistically significant decrease in symptom prevalence or severity over the 14-day study period.
At each visit, participants reported their overall severity of coronavirus disease 2019 (COVID-19) symptoms on a continuous visual analogue scale of 0–10 points. The primary end point (overall change in symptom severity score) was calculated with linear mixed-effects models, adjusted for baseline severity score. Hydroxychloroquine was associated with a 12% relative difference over placebo, based on an absolute difference of −0.27 (95% CI, −0.61 to 0.07; P = 0.117) on the visual analogue scale. Supplement Table 4 shows mean values and 95% CIs. At day 5, symptom severity had worsened from baseline in 16% of participants receiving hydroxychloroquine and 20% of those receiving placebo.
We analyzed a priori–defined, baseline subgroups by change in symptom severity score through 14 days (Figure 5). Subgroup results were generally consistent with the overall result. Of note, inclusion of persons without a laboratory-confirmed diagnosis did not dilute the hydroxychloroquine effect because there was no significant interaction between those who had PCR-confirmed disease (nonsignificant 5.2% relative improvement) and those who did not have PCR-confirmed disease (nonsignificant 14.7% relative improvement) (P for interaction = 0.51). We explored the change in symptom severity score by medication adherence as a post hoc analysis and found improvement in those receiving hydroxychloroquine compared with placebo when they took at least 75% of the prescribed study medication (19.5% relative benefit). However, within the hydroxychloroquine group, improvement in symptom scoring by day 14 did not differ between participants who were more than 75% adherent (change, −2.57 points) and those who were less than 75% adherent (change, −2.70 points). Additional post hoc analyses showed that self-reported use of zinc or vitamin C in addition to hydroxychloroquine did not improve symptoms over use of hydroxychloroquine alone (Supplement Table 2).
Mean change from baseline and estimated difference from a longitudinal mixed model adjusted for baseline severity score. P values for trend of continuous variables are in parentheses. Subgroups were defined a priori in the protocol. The final diagnosis includes all diagnostic testing results during the study period. Probable diagnosis is based on the U.S. clinical case definition (10). The final diagnosis categories are hierarchical as listed (and thus mutually exclusive). Participants with symptom duration of 1–2 d before enrollment in the hydroxychloroquine group had a larger reduction in symptom score than those receiving placebo, but this was not observed in those who enrolled with symptom durations <1 d, where one might expect an even greater effect if hydroxychloroquine therapy helped mitigate disease severity if started very early in the disease course. Additional post hoc subgroups of medication adherence, zinc, and vitamin C are presented in Supplement Table 2.
The incidence of hospitalization or death was 3.2% (15 of 465) among participants with known vital status. With hydroxychloroquine, 4 hospitalizations and 1 nonhospitalized death occurred (n = 5 events). With placebo, 10 hospitalizations and 1 hospitalized death occurred (n = 10 events); of these hospitalizations, 2 were not COVID-19–related (nonstudy medicine overdose and syncope). The incidence of hospitalization or death did not differ between groups (P = 0.29).
On completion of the study medication regimen, 77% (157 of 203) of participants receiving hydroxychloroquine reported complete adherence to the regimen, compared with 86% (166 of 194) receiving placebo. Adverse effects were more common in those receiving hydroxychloroquine than placebo through the 5-day regimen (43% [92 of 212] vs. 22% [46 of 211]; P < 0.001). With hydroxychloroquine, gastrointestinal symptoms were the most commonly reported adverse effect: 31% (66 of 212) of participants reported upset stomach or nausea, and 24% (50 of 212) reported abdominal pain, diarrhea, or vomiting (Supplement Table 3). We observed no association between the presence of adverse effects and that of symptoms (Supplement Table 8). Adverse effect prevalence decreased markedly after day 5. No serious adverse events attributable to the study drug occurred.
We assessed the efficacy of study medicine masking on day 14. Of the 194 participants who completed day-14 surveys in the intervention group, 49% (n = 94) correctly identified that they had received hydroxychloroquine, 7% (n = 14) believed that they had received placebo, and 44% (n = 86) were unsure. Of the 182 who completed day-14 surveys in the placebo group, 30% (n = 54) correctly guessed placebo, 25% (n = 46) incorrectly guessed hydroxychloroquine, 42% (n = 76) were unsure of their randomization assignment, and 3% (n = 6) did not respond. Thus, masking was generally effective, with adverse effects markedly differing between groups.
Discussion
In this randomized, double-blind, placebo-controlled trial of symptomatic outpatient adults with probable or confirmed early COVID-19, a 5-day course of hydroxychloroquine failed to show a substantial clinical benefit in improving the rate of resolution of COVID-19 symptoms in the enrolled clinical trial participants. Of those receiving placebo, 70% reported no COVID-19 symptoms by day 14 of the study, 96% had not been hospitalized, and 99.6% survived. The change in symptom severity was not statistically significant: only a 12% relative improvement over placebo. For comparison, oseltamivir in influenza showed a 25% to 35% relative reduction in symptom severity score in clinical trials (16, 17). Therefore, the modest clinical effect that practitioners ascribe to oseltamivir is still 2-fold greater than that observed with hydroxychloroquine.
To our knowledge, this is the first randomized clinical trial investigating treatment of COVID-19 among outpatients (a search of PubMed and MEDLINE on 24 June 2020 for publications in all languages using the keyword COVID-19 revealed no published outpatient randomized clinical trials). This builds on other randomized trial data on hydroxychloroquine, which have not shown any benefit for postexposure prophylaxis or for treatment of hospitalized patients (11, 18, 19). In addition, after this trial was completed, in vivo animal models have reported no hydroxychloroquine activity against SARS-CoV-2 in hamsters, ferrets, or nonhuman primates (20–22).
Change in symptom severity score using a 10-point continuous visual analogue scale is a clinically relevant end point describing participant improvement over time. Validated scoring instruments for symptom severity were not yet available for outpatients with COVID-19 when we designed this trial. Although the visual analogue scale is a subjective measure, the within-person measurement of symptom severity is internally consistent over time. For our outpatient trial, time to resolution of an individual symptom was not considered appropriate because individuals presented with differing symptoms. For example, 65% had cough, and 38% had fever. In addition, some isolated symptoms, such as fatigue, may persist after the overall syndrome subsides. Thus, we believe that the intraperson change in overall symptom severity over time represents a clinically meaningful end point, particularly in a disease that exhibits such heterogeneous symptomatology. Using a continuous end point results in smaller sample sizes than required for categorical or ordinal end points—thereby expediting phase 2 trials and allowing early assessment of potential clinical benefit.
Our original end point was an ordinal outcome of reduced hospitalization, intensive care unit stay, or death. Among the enrolled participants, the incidence of hospitalization was only 3% and incidence of death only 0.4%, making the planned analysis of the ordinal end point futile. We do note that 8 COVID-19–related hospitalizations (including 1 death) occurred with placebo versus 4 COVID-19 hospitalizations (and 1 additional death; 5 events in total) with hydroxychloroquine. Our population was relatively young with 77% of participants being aged 50 years or less, with few comorbid conditions; thus, our trial findings are most generalizable to such populations. It is possible that hydroxychloroquine is more effective in populations at higher risk for complications, such as older persons in long-term care facilities (23). Performing randomized trials in long-term care facilities could test whether hydroxychloroquine can reduce hospitalizations; however, the risk for medication adverse effects and drug–drug interactions will also be higher (24).
The primary limitation of our trial is the lack of confirmed SARS-CoV-2 infection in all participants, although participants met international and U.S. COVID-19 case definitions (10, 25). The trial began on 22 March 2020, when PCR testing supplies were severely limited in the United States with outpatients ineligible for testing or with frequent delays in receiving test results. We countered this by enrolling participants with known epidemiologic links to index cases with PCR positivity and proven high-risk exposures. The use of epidemiologic linkage to enroll symptomatic persons is both a limitation and a strength. Although these persons did not have PCR-confirmed diagnoses, using epidemiologically linked cases enabled rapid enrollment after symptoms began: 56% of participants enrolled within 1 day of symptom onset. Only 16% of participants contributing data to the primary end point had a confirmed negative result on a PCR test; this falls within the known false-negative rate of current molecular techniques (8). In subgroup analyses, participants with epidemiologic linkage or probable COVID-19 by case definition only had similar responses to those with PCR-confirmed COVID-19. PCR-confirmed cases had the least effect observed.
In conclusion, finding effective therapies against COVID-19 remains critical. Effective treatment of early, outpatient COVID-19 could decrease hospitalizations and, ultimately, morbidity and mortality. Hydroxychloroquine did not substantially reduce symptom severity or prevalence over time in nonhospitalized persons with early COVID-19. This trial may not inform whether an effect would be observed in populations at higher risk for severe COVID-19. Further randomized controlled clinical trials are needed in early COVID-19.
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Kaptein SJF ,Jacobs S ,Langendries L ,et al . Antiviral treatment of SARS-CoV-2-infected hamsters reveals a weak effect of favipiravir and a complete lack of effect for hydroxychloroquine. bioRxiv. Preprint posted online 19 June 2020. doi:10.1101/2020.06.19.159053 CrossrefGoogle Scholar - 21.
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Maisonnasse P ,Guedj J ,Contreras V ,et al . Hydroxychloroquine in the treatment and prophylaxis of SARS-CoV-2 infection in non-human primates. Research Square. Preprint posted online 6 May 2020. doi:10.21203/rs.3.rs-27223/v1 CrossrefGoogle Scholar - 23.
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Author, Article, and Disclosure Information
Caleb P. Skipper,
University of Minnesota, Minneapolis, Minnesota (C.P.S., K.A.P., N.W.E., A.S.B., M.A., S.M.L., D.A.W., E.C.O., M.F.P., M.R.N., A.A.N., K.H.H., R.R., D.R.B.)
Research Institute of the McGill University Health Centre and McGill University, Montréal, Quebec, Canada (M.P.C., E.G.M., T.C.L.)
M Health Fairview Investigational Drug Service Pharmacy, Minneapolis, Minnesota (D.L.)
University of Manitoba, Winnipeg, Manitoba, Canada (S.A.L., L.J.M., G.D., R.Z.)
George & Fay Yee Centre for Healthcare Innovation, Winnipeg, Manitoba, Canada (L.E.K.)
University of Alberta, Edmonton, Alberta, Canada (I.S.S.)
Acknowledgment: The authors thank the research volunteers for consenting to participate in this trial and the late Dr. Charlie Van der Horst for inspiration in infectious diseases research and a commitment to social justice. They also thank the trial's research collaborators, Alyssa Agostinis, Sarah Elsayed, Derek LaBar, Alek Lefevbre, Nicole Marten, Kristen Moran, and Lulu Smith.
Financial Support: By Steve Kirsch, Jan and David Baszucki, the Minnesota Chinese Chamber of Commerce, the Alliance of Minnesota Chinese Organizations, and the University of Minnesota Foundation. Drs. Nicol, Rajasingham, and Pullen are supported by the National Institute of Allergy and Infectious Diseases (K08AI134262, K23AI138851, and T32AI055433). Dr. Lofgren is supported by the National Institute of Mental Health (K23MH121220). Dr. Skipper is supported by a combined Fogarty International Center/National Institute of Neurological Disorders and Stroke grant (D43TW009345). Ms. Pastick and Ms. Okafor are Doris Duke International Clinical Research Fellows supported through the Doris Duke Charitable Foundation. Drs. Boulware, Hullsiek, Engen, and Bangdiwala are supported by grants R01AI118511 and U01AI125003 from the National Institutes of Health, with an emergency supplement request made. Drs. Lee and McDonald receive salary support from the Fonds de recherche du Québec – Santé. Canadian funding was received from various sources. In Quebec, funds were received from the Clinical Practice Assessment Unit of the McGill University Health Centre and the McGill Interdisciplinary Initiative in Infection and Immunity's Emergency COVID-19 Research Funding. In Manitoba, research support was received from the Manitoba Medical Service Foundation and Research Manitoba. Purolator Canada provided in-kind courier support for the participating Canadian sites. Apotex Canada and Rising Pharmaceuticals in the United States provided a donation of some of the hydroxychloroquine tablets used.
Disclosures: Disclosures can be viewed at www.acponline.org/authors/icmje/ConflictOfInterestForms.do?msNum=M20-4207.
Data Sharing Statement: The following data will be made available beginning 22 July 2020: deidentified participant data, data dictionary (covidpep.umn.edu). The following supporting documents will be made available with publication: informed consent form (ClinicalTrials.gov). These data will be made available for open access (restrictions: none).
Corresponding Author: David R. Boulware, MD, MPH, 689 23rd Avenue, Minneapolis, MN 55455; e-mail, faq.
Current Author Addresses: Drs. Skipper, Abassi, Lofgren, Pullen, Rajasingham, and Boulware; Ms. Pastick; Ms. Williams; and Ms. Okafor: 689 23rd Avenue SE, Minneapolis, MN 55455.
Ms. Engen, Ms. Bangdiwala, and Dr. Hullsiek: School of Public Health, University of Minnesota, 2221 University Avenue SE, Suite 200, Minneapolis, MN 55414.
Dr. Nicol: 2001 6th Street SE, MTRF 4-210, Minneapolis, MN 55455.
Ms. Nascene: Department of Psychiatry, 717 Delaware Street SE, Suite 516, Minneapolis, MN 55414.
Dr. Cheng: Divisions of Infectious Diseases and Medical Microbiology, McGill University Health Centre, 1001 Décarie Boulevard, Room E05.1709, Montréal, QC H4A 3J1, Canada.
Ms. Luke: 420 Delaware Street SE, MMC 611 Mayo, Minneapolis, MN 55455.
Dr. Lother: JJ399-820 Sherbrook Street, Winnipeg, MB R3A 1R9, Canada.
Dr. MacKenzie: 543 Basic Medical Sciences Building, 745 Bannatyne Avenue, Winnipeg, MB R3E 0J9, Canada.
Dr. Drobot: C5010 - 409 Taché Avenue, Winnipeg, MB R2H 2A6, Canada.
Dr. Kelly: 417-753 McDermot Avenue, Winnipeg, MB R3E 0T6, Canada.
Dr. Schwartz: 1-124 Clinical Sciences Building, 11304-83 Avenue NW, Edmonton, AB T6G 2G3, Canada.
Dr. Zarychanski: ON4005 – 675 McDermot Avenue, Winnipeg, MB R3M 3M6, Canada.
Dr. McDonald: 5252 De Maisonneuve, Room 3E.03, Montréal, QC H4A 3S9, Canada.
Dr. Lee: 1001 Décarie Boulevard, Room E5.1820, Montréal, QC H4A 3S1, Canada.
Author Contributions: Conception and design: C.P. Skipper, K.A. Pastick, M. Abassi, S.M. Lofgren, M.F. Pullen, M.R. Nicol, K.H. Hullsiek, L.J. MacKenzie, R. Zarychanski, R. Rajasingham, D.R. Boulware.
Analysis and interpretation of the data: C.P. Skipper, K.A. Pastick, N.W. Engen, A.S. Bangdiwala, S.M. Lofgren, E.C. Okafor, M.F. Pullen, M.R. Nicol, K.H. Hullsiek, I.S. Schwartz, R. Zarychanski, T.C. Lee, R. Rajasingham, D.R. Boulware.
Drafting of the article: C.P. Skipper, K.A. Pastick, N.W. Engen, A.S. Bangdiwala, M. Abassi, S.M. Lofgren, E.C. Okafor, M.F. Pullen, A.A. Nascene, L.J. MacKenzie, G. Drobot, L.E. Kelly, T.C. Lee, D.R. Boulware.
Critical revision of the article for important intellectual content: C.P. Skipper, S.M. Lofgren, M.F. Pullen, M.R. Nicol, K.H. Hullsiek, M.P. Cheng, S.A. Lother, L.J. MacKenzie, L.E. Kelly, I.S. Schwartz, E.G. McDonald, T.C. Lee, R. Rajasingham, D.R. Boulware.
Final approval of the article: C.P. Skipper, K.A. Pastick, N.W. Engen, A.S. Bangdiwala, M. Abassi, S.M. Lofgren, D.A. Williams, E.C. Okafor, M.F. Pullen, M.R. Nicol, A.A. Nascene, K.H. Hullsiek, M.P. Cheng, D. Luke, S.A. Lother, L.J. MacKenzie, G. Drobot, L.E. Kelly, I.S. Schwartz, R. Zarychanski, E.G. McDonald, T.C. Lee, R. Rajasingham, D.R. Boulware.
Provision of study materials or patients: M.F. Pullen, M.P. Cheng, D. Luke, G. Drobot, L.E. Kelly, I.S. Schwartz, E.G. McDonald, T.C. Lee.
Statistical expertise: N.W. Engen, A.S. Bangdiwala, K.H. Hullsiek.
Obtaining of funding: M.P. Cheng, R. Zarychanski, E.G. McDonald, T.C. Lee, D.R. Boulware.
Administrative, technical, or logistic support: C.P. Skipper, K.A. Pastick, A.S. Bangdiwala, S.M. Lofgren, D.A. Williams, E.C. Okafor, M.F. Pullen, A.A. Nascene, S.A. Lother, L.E. Kelly, I.S. Schwartz, T.C. Lee, D.R. Boulware.
Collection and assembly of data: C.P. Skipper, K.A. Pastick, A.S. Bangdiwala, M. Abassi, D.A. Williams, E.C. Okafor, M.F. Pullen, A.A. Nascene, L.J. MacKenzie, L.E. Kelly, I.S. Schwartz, E.G. McDonald, T.C. Lee, D.R. Boulware.
This article was published at Annals.org on 16 July 2020.
Where is the power?
I read with great interest the paper published by Skipper et al on Hydroxychloroquine in Nonhospitalized Adults With Early COVID-19: A Randomized Trial (Ann Intern Med. 2020 Jul 16. doi: 10.7326/M20-4207).
I tried to calculate the power of their results from Figure 3, considering that symptoms were 24.4% and 30.4% in the hydroxychloroquine (n=201) and placebo (194) group respectively. Post-hoc test for power was 26.7%; if these are the results, the implications are quite serious.
Furthermore, I would expect a more rigorous study. The heavily criticized [1] article published by Gautret et al., the French group used RT-PCR results as the main outcome in patients [2].
In the study presented by Skipper et al. , they used self-reported survey data using the REDCap system, i.e., individuals would have to access the internet and send their impressions.
Sadly enough, the major headlines present that hydroxychloroquine does not work. At least, they found that the incidence of side effects is lower than it has been announced.
References
1 eliesbik. Thoughts on the Gautret et al. paper about Hydroxychloroquine and Azithromycin treatment of COVID-19 infections. Science Integrity Digest. 2020.https://scienceintegritydigest.com/2020/03/24/thoughts-on-the-gautret-et... (accessed 17 May 2020).
2 Gautret P, Lagier J-C, Parola P, et al. Hydroxychloroquine and azithromycin as a treatment of COVID-19: results of an open-label non-randomized clinical trial. Int J Antimicrob Agents 2020;:105949.
Is it time to exclude efficacy for hydroxychloroquine in early COVID-19?
We read with interest the article from Skipper et al about the use of hydroxychloroquine for treatment of early outpatient patients with COVID-19 compatible symptoms or confirmed diagnosis (1). Despite the absence of statistically significant difference in any of the selected outcomes, the negative results of that pertinent study must be interpreted with caution. At first, the study authors established initially as primary outcome an ordinal scale of disease severity (outpatient, inpatient, ICU, death). The evaluation was influenced by the lower than expected incidence of hospitalizations, requiring after interim analysis the change of the primary outcome. Another relevant issue is that the study was originally sized to find a 50% reduction in those outcomes, which seems utopic.
Surprisingly, hydroxychloroquine group had 50% lower incidence of a composite outcome for hospitalization and death for any cause (reported P = 0.29). Hydroxychloroquine treated patients had 24% of patients with persistence of COVID-19 compatible symptoms at 14 days, versus 30% of placebo, denoting a non-significant absolute reduction of 20% between groups (P = 0.21). If confirmed in adequately dimensioned trials, this difference is clinically meaningful. The new primary outcome, mean reduction from baseline in a 10-point visual analogue scale (VAS) for disease severity, at day 14 was close to one in the placebo group, indicating lack of relevance of that endpoint in practice at that time of follow-up. Nevertheless, at 10 days of randomization (11 to 14 days after the start of the symptoms) there was a 0.42 points absolute reduction in VAS scale (P = 0.050).
Hydroxychloroquine use in patients with COVID-19 has a low a priori belief of clinical benefit due to unavailable translational evidence, lack of benefit in previous research with other viruses, and no benefit in previous adequately performed observational research and randomized controlled trials (2,3). The absolute results reported must be considered with caution and interpreted within the limits of the confidence interval for all outcomes. Naturally, the results of this study do not support the use of hydroxychloroquine in early COVID-19. However, the present study findings offer an insight for future research in such specific population and not a proof of lack of any clinically relevant benefit.
Conflicts of interest: none.
References
1. Skipper CP, Pastick KA, Engen NW, Bangdiwala AS, Abassi M, Lofgren SM, et al. Hydroxychloroquine in Nonhospitalized Adults With Early COVID-19. Annals of Internal Medicine [Internet]. 16 de julho de 2020 [citado 18 de julho de 2020]; Disponível em: https://www.acpjournals.org/doi/10.7326/M20-4207
2. Schluger NW. The Saga of Hydroxychloroquine and COVID-19: A Cautionary Tale. Annals of Internal Medicine [Internet]. 16 de julho de 2020 [citado 18 de julho de 2020]; Disponível em: https://www.acpjournals.org/doi/10.7326/M20-5041
3. A Randomized Trial of Hydroxychloroquine as Postexposure Prophylaxis for Covid-19 | NEJM [Internet]. [citado 18 de julho de 2020]. Disponível em: https://www.nejm.org/doi/full/10.1056/NEJMoa2016638
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It is unfortunate that zinc was not administered concomitantly. I would like to see a similar trial with zinc, and also with an option for long term periodic follow up, since we are beginning to see complications emerge weeks later. Zinc makes sense from a pharmacological standpoint, and it is not surprising that without zinc the hydroxychloroquine is not effective.
Disclosures:
None
Symptom severity: A surrogate for disease severity?
Comment: Authors of the present study should be commended for their work to determine the role of hydroxychroloquine for reducing severity of symptoms due to coronavirus disease 2019 (COVID-19). Notwithstanding the fact that more than 50% of study participant's test reports were unknown for novel coroanvirus (SARS-CoV-2), I have few comments to make.
Investigators of the study should have stated the reason for considering symptoms severity as a surrogate for disease severity for clarity of novice readers like me. Severity of symptoms is not directly correlated to severity of the disease or in this case COVID-19. As treating doctors, we emphasize on clinical signs to determine disease severity, which everyone follows. For example, if I report cough or shortness of breath today, my symptom severity over the next few days will be different from another person, because of my resilience, prior experience of cough or breathing difficulty, and my present status of health, etc. Authors of the study note that eight COVID19 -related hospitalizations (including 1 death) occurred with placebo versus 4 COVID-19 hospitalizations (and 1 additional death; 5 events in total) in the other arm, but fails to mention the cause of death in nonhospitalized patient in the hydroxychroloquine arm. The authors should investigate the cause of death of the patient in hydroxychroloquine arm. In case death of that patient is not due to COVID-19, then there is around 40% reduction (P = 0.29) in hospitalization and death in the hydroxychroloquine arm, though events (n=15) were too less for such a conclusion. Authors mention in the discussion “our trial findings are most generalizable to populations below 50 years of age” and further suggest “performing randomized trials in long-term care facilities could test whether hydroxychloroquine can reduce hospitalizations”.
However, the accompanying editorial concludes “it is time to move on from hydroxychloroquine”. It appears there is a bias for writing the epitaph for hydroxychroloquine sooner than later! The editorial states "many good ideas in medicine do not work" . Yes, I agree, but who determines which idea is working or not. In this case, insufficient evidences are being presented to "kill an idea"
Wrong group studied.
This study, with 77% of the participants age 50 or below, does not answer the most critical question; can early use of hydroxychloroquine, or chloroquine, reduce the incidence of severe disease and death. About half of Covid-19 deaths in the U.S. occur in the age 65+ group, about 80% in Canada; this is the group that should be studied, and all the participants should have a positive test before inclusion. The lay press will give undeserved credence to this paper.
Disclosures:
Author does not have any conflict of interests
Is Hydroxychloroquine effective in non-hospitalized adults with early COVID-19?
Dear Editor,
We read with interest the article titled “Hydroxychloroquine in non-hospitalized adults with early COVID-19: A randomized trial” by Caleb Skipper et al published on 16 July 2020.1
The authors demonstrate only a 12% relative improvement in symptom severity over placebo in patients taking Hydroxychloroquine (HCQ). However, there are some confounders in the study. Study participants (423) were those who completed at least 1 follow-up survey with symptom data. The outcome would be impacted if some participants did not complete all the follow up surveys with this small sample size.
The number of hospitalization and/or death were half (n=5) in the HCQ group as compared to the placebo group (n=10), giving a ‘p’ value of 0.2. As discussed in the statistics section, the primary endpoint was changed from the ordinal outcome of not-hospitalized, hospitalized, intensive care unit stay or death to overall symptom severity during the first interim analysis, due to the substantially lower event rate than expected. This was because the authors decided that a sample size of 6000 participant is needed to show difference in the event rates, which was considered impossible at that time. Therefore, the doubling of event rate in this relatively small sample size cannot be ignored and needs further evaluation.
There were fewer (77%) participants receiving HCQ who reported complete adherence to the regimen compared with those receiving placebo (86%) likely reducing the performance of HCQ in this study.
Among hospitalized patients, use of HCQ alone and in combination with azithromycin has been demonstrated to be associated with a significant reduction in-hospital mortality compared to not receiving HCQ.2 Further, consumption of four or more maintenance doses of HCQ has been shown to be associated with a significant decline in the odds of getting infected.3 In view of above points, a larger sample size study would be worthwhile to see if HCQ performs better than placebo in non-hospitalized adults with COVID-19.
References
Disclosures:
The authors disclose no conflict of interest.
Hydroxychloroquine: an age- and stage- nuanced, clinically and economically meaningful COVID-19 strategy?
Hydroxychloroquine’s (HCQ) apparent inefficacy, with generally safe use in mild COVID-19, reported by Skipper et al.1 and similar RCTs (Tang, cited in2; Mitja3), might be unsurprising given data in more severe disease cited by the accompanying editorial2 were not a consideration of methodology, age, comorbidity and disease stage to suggest otherwise.
Skipper’s initial endpoint of at least hospitalization proved inappropriate; a problem shared by Mitja.3 Mitja’s use of nasopharyngeal viral load reduction suffers from acknowledged limitations, test unreliability, and temporo-spatial differences in viral shedding in the respiratory tract.4 Further challenging are Skipper’s unvalidated and left-censored symptom VAS and possible activity5 of the folate placebo, an issue shared by its companion post-exposure prophylaxis study.6
Categorical measures of disease persistence are (other than their comparisons being underpowered in these already small studies) undiluted by a large majority of participants with good prognoses and, more reliably and meaningfully, inform economically devastating lockdown decisions, driven partly by resource consumption. A 20% relative reduction of symptom persistence from 30% to 24% with HCQ could non-trivially preserve healthcare and essential worker resources and limit (still poorly understood) infectivity of symptomatic cases. Mitja’s3 reduction of hospitalization from 7.1% to 5.9% (reported as RR 0.75) could be similarly meaningful as would Tang’s finding of a 22% reduction in persistence of PCR positivity associated with HCQ from 18.7% to 14.6%.
Obscured by considering VAS changes is an apparent population bimodality (“improvers” vs. “non-improvers”) that could be exploited to stratify risk. With only 24% and 30% of participants accounting for the 28-day VAS of 1.5 (HCQ) and 1.87 (placebo) respectively, average scores in still-symptomatic patients increased to 6.15 and 6.14 respectively.
With no treatment options on the immediate horizon, the secondary surging of COVID-19, the prospect of more lockdowns and their economic consequences, further analysis of this study and related studies is demanded before decisions to abandon HCQ are made. The possibility must also be entertained that zinc or ascorbate, used prevalently and without definition here, may accomplish as much as HCQ in this population.
Along with suggestions of an effect of HCQ in younger subjects for early post-exposure prophylaxis6 as well as synergy between HCQ and zinc7 or methylprednisolone8 in more severe cases, the Skipper and related studies support prospective evaluation of a stage- and age- nuanced approach to COVID-19.
References
Disclosures:
Author does not have an conflict of interest
Patients who never started treatment kept in analysis
We read the article intitled “Hydroxychloroquine in nonhospitalized adults with COVID-19”, by Skipper et al, with much interest. We disagree with some of the authors’ conclusions, which we believe could not be taken from the data shown.
(1) In suppl table 3, concerning medication adherence, the sum of all categories in HCQ group is: 100% of the tablets, 157; 75-99% of the tablets, 8; <75% of the tablets, 16; never started medication, 22, so = 157+8+16+22= 203. In placebo group, the sum of these categories is 166+3+12+13=194. In suppl table 2, concerning the analysis of symptoms severity according to medication adherence, table states that in HCQ group, 165 patients took >75% of the tablets (15-19) and 38 <75% (1-14), 165+38= 203. In placebo group, 169+25= 194. Comparing these two tables, it becomes clear that in suppl table 2 if category <75% was in fact 1-14 tablets, we should be missing 22 patients in group HCQ and 13 patients in placebo group, who never started medication (0 tablets). Since we are not missing them, in both tables group HCQ has 203 patients and group placebo has 194 patients, I assume the author kept patients who never started medication in HCQ and placebo groups. It is not a question of writing 0-14 instead of 1-14 tablets; it is about excluding patients who did not start treatment from ITT analysis. The “1-14 tablets” induces the reader to assume that authors performed the usual analysis, excluding patients who did not start treatment. We recall that even in intention-to-treat analysis, if no treatment was applied at all, the usual procedure is to exclude these patients from the full analysis set. https://www.clinfo.eu/itt-vs-pp/
(2) We acknowledge that ignoring those patients who stopped the medicine because of side effects introduces biases. However, it does not apply to this situation, since these 22 patients who never started HCQ treatment never experienced any side effects and there were also 13 patients who never started placebo; they did not start treatment for reasons not related to group allocation. While no biases might arise from excluding patients who never started treatment allocated to both HCQ and placebo groups, keeping them in the full analysis set might mask any positive HCQ effects. Masking the positive effects of a drug during a pandemic is a harmful choice.
(3) If a medication is found to work under optimal conditions in the trial setting, the adherence to this medication in the field will be far better. We recall that the uncertainty about the efficacy of a drug being tested in the trial setting may mean that trial participants are less likely to persevere with unpleasant side effects of treatment than those who have been assured of the efficacy of their treatment (1). Yet the authors seem to disregard their own HCQ positive results found when patients taking >75% of the tablets are considered, a significant 19.5% relative benefit in symptom severity (two-tailed p-value=0.022).
(4) Authors “caution against over-interpretation of this result”, a 19.5% relative benefit in symptom severity, arguing that “this [adherent HCQ] group did not improve any more than the non-adherent hydroxychloroquine group nor the non-adherent placebo group”. However, unlike comparison between treated and untreated group, the comparison between adherent and non-adherent group is invalid as the latter groups are not selected by randomization and are subject to “non-adherence bias”, i.e., non-adherent patients might have not taken the drug for instance because they were healthier than adherent patients. This is corroborated by the data in the table which shows that the small non-adherent group did overall much better than the larger adherent group.
(5) We understand that the proper way to analyze the data is by doing both an analysis of the intention-to-treat population (excluding, as usual, patients who took zero tablets) and a per protocol analysis of the patients with 75% adherence to the treatment.
The consequence of these considerations is that conclusions such as the one in the abstract and discussion, “hydroxychloroquine did not substantially reduce symptom severity in outpatients with early, mild COVID-19”, cannot be assumed when a possible positive effect might arise from the rightful exclusion of patients who never started treatment and there is a clear 19.5% effect of hydroxychloroquine over placebo when patients who took the tablets are compared, i.e., per-protocol analysis.
Claudia Neto Paiva – Associate Professor, Instituto de Microbiologia, Universidade Federal do Rio de Janeiro, Brazil
Daniel Victor Tausk – Associate Professor, Instituto de Matemática e Estatística, Universidade de São Paulo
Authors' response to Pavia and Tausk, Bruno Luís de Castro Araujo
In response to Pavia and Tausk, the a priori written protocol and statistical analysis plan called for an intent-to-treat analysis, whereby everyone randomized was analyzed. A modified intent to treat analysis has similar results when excluding those who did not start study medicine, including open-label hydroxychloroquine use (n=1), and carryforward of symptom status for those hospitalized, dead, or with resolved symptoms at day 10. Ongoing symptoms were present at day +5 in 54.9% (100/182) receiving hydroxychloroquine and 57.5% (104/181) receiving placebo. At day +14, ongoing symptoms were present in 24.9% (46/185) who received hydroxychloroquine and 31.1% (56/180) who received placebo. The number needed to treat (NNT) to have 1 additional person be without symptoms at day 14 is 16 persons (95%CI, -34(harm) to 6.5). In restricting to those with 100% adherence to hydroxychloroquine, 25.2% (39/155) of participants had ongoing symptoms at day 14. The original intention-to-treat analysis in the manuscript reported 24.4% vs. 30.4% having symptoms at day 14. Thus, whether modified intention-to-treat or per protocol analysis, the original conclusions remain the same.
Supplemental Table 2 does have a typo in the label of “<75% adherence” which should include zero tablets in the label of <75% adherence. Supplemental Table 3 presents the breakdown on study medicine adherence. A “per protocol analysis” is generally recognized as a biased analysis as this ignores those who stop medications due to side effects. Those who cannot complete a treatment cannot be expected to benefit from the therapy. In this randomized double-blind trial, <100% adherence (range 5-89%) occurred more frequently with hydroxychloroquine at 11.8% (24/203) than with placebo at 7.8% (15/194), most often due to medication side effects or spontaneously improving. At study day 5 when adherence was assessed, among those with 100% adherence, 54.1% (85/157) had ongoing symptoms with hydroxychloroquine versus 56.6% (94/166) with placebo. This minimally differs from the modified intent-to-treat analysis.
In response to Bruno Luís de Castro Araujo, we did not find a statistical difference in covid-related hospitalizations or death (2.2% [5/231] with hydroxychloroquine vs. 3.4% [8/234] with placebo). Whether the magnitude of benefit would be greater in a higher risk population at a greater risk of severe disease, is unknown, as mentioned in the discussion. In a similar early outpatient hydroxychloroquine trial in Barcelona (n=293), Mitja and colleagues found zero virologic effect of hydroxychloroquine (+0.07 log10 copies/mL higher at 7 days, 95%CI, -0.29 lower to 0.44 higher).(1) Their incidence of hospitalization was 5.9% (8/136) with hydroxychloroquine versus 7.0% (11/157) with standard of care in Catalonia.(1) Whether this trend of ~1.3% reduction in hospitalization (95%CI, -1.5% to 4.2%) in the two trials is indeed a real statistically significant difference is the subject of ongoing efforts to pool data across 8 early treatment trials to generate a larger sample size. At present, there is no statistical difference with a NNT of 76 (95%CI, -65(harm) to 24) to prevent a hospitalization in the population studied to date in these two trials, which has encompassed approximately 70% healthcare workers with a median age of ~40 years. Other early treatment trials are ongoing, and outpatient PCR testing in the United States has greatly expanded since our trial’s conduct in March and April 2020.
Hydroxychloroquine (HCQ) vs. folic acid: evaluation of absolute efficacy or relative efficacy against COVID agents?
Dear editor,
We read with great interest, the published randomized control trial by Skipper et al [1] in your esteemed journal. It is a well conducted multicentered trial, conducted in two locations (United states and Canadian provinence) with the intention to evaluate the absolute “therapeutic efficacy” of hydroxychloroquine in “symptomatic non-hospitalized” adults. Patients were randomly allocated into either hydroxychloroquine or and placebo arm. While looking into the composition of placebo we could find that folic acid tablet 400 mcg was used as placebo in the US population and lactose tablet in Canada population.
Respected Sir, in in-silico studies folic acid came as a good binder against SARS-CoV-2 furin (required for viral entry to host cell) [2]. In clinical studies, Itelman et al [3] reported lower blood folic acid levels among patients with severe disease compared to those with mild disease. Pregnant women appears to be less likely to require a hospitalization from COVID-19 [4] and Acosta-Elias J et al, 2020 postulated that “folic acid” uptake may be the protective factor. A product Angiovit (containing folic acid & vitamin B12) is associated with a lower duration of “hospital stay” and “fever” compared to control [5]. Many trials evaluating folic acid as therapeutic agent against COVID-19 are currently under way (NCT04354428, PACTR202005599385499).
Skipper et al, 2020 [1], concluded that there was no statistically significant difference in terms of “COVID-19 related symptoms”, “incidence of hospitalization” and “death” between both the arms. This comparable efficacy does not indicate the absolute efficacy of HCQ; rather we can say its comparative efficacy between HCQ and folic acid and both performed equally. Again, rather than calling this trial a placebo controlled trial, it will be better to address as a “head-on” comparison between HCQ and folic acid.
Bibliography
Disclosures:
None of the authors declared any conflict of interest
Authors' Response to Pavia and de Castro Araujo
In response to Pavia, the protocol and statistical analysis plan called for intent-to-treat analysis, whereby everyone randomized was analyzed. A modified intent to treat analysis has similar results when excluding those who did not start study medicine, who used open-label hydroxychloroquine (n=1), and with carryforward of symptom status for those hospitalized, dead, or with resolved symptoms at day 10. Ongoing symptoms were present at day +5 in 54.9% (100/182) receiving hydroxychloroquine and 57.5% (104/181) receiving placebo. At day +14, ongoing symptoms were present in 24.9% (46/185) who received hydroxychloroquine and 31.1% (56/180) who received placebo. The number needed to treat (NNT) to have 1 additional person be without symptoms at 14 days is 16 persons (95%CI, -34(harm) to 6.5). The original intention-to-treat analysis reported 24.4% vs. 30.4% having symptoms at day 14 (1).
A “per protocol analysis” is generally recognized as a biased analysis as this ignores those who stop medications due to side effects. In this randomized double-blind trial, <100% adherence (range 5-89%) occurred more frequently with hydroxychloroquine (11.8%, 24/203) than with placebo (7.8%, 15/194), often due to medication side effects or spontaneous improvement. As Supplemental Table 2 presents, those with <75% adherence, which includes those never starting the medicine, had greater resolution of symptom severity. Yet when restricting to those with 100% adherence as a per protocol analysis, ongoing symptoms existed at day 5 in 54.1% (85/157) receiving hydroxychloroquine versus 56.6% (94/166) receiving placebo. At day 14, 25.2% (39/155) of hydroxychloroquine participants had ongoing symptoms. Thus neither a modified intent-to-treat or per protocol analysis substantially differs from the original intent-to-treat analysis.
In response to Bruno Luís de Castro Araujo, we did not find a statistical difference in COVID-related hospitalizations or death (2.2% [5/231] with hydroxychloroquine vs. 3.4% [8/234] with placebo). Two non-COVID events occurred in the placebo arm requiring hospital observations of <24 hours. In a similar early outpatient treatment randomized trial (n=293), Mitja and colleagues found zero virologic effect of hydroxychloroquine (+0.07 log10 copies/mL higher at 7 days) compared with no therapy (2). Their incidence of all-cause hospitalization was 5.9% (8/136) with hydroxychloroquine versus 7.0% (11/157) with standard of care in Catalonia (2). Whether this 1.3% reduction in hospitalizations (95%CI, -1.5% to 4.2%) in the two trials is a real difference requires further data (1, 2). A third large randomized trial in Brazil was halted for futility with no effect on hospitalization or death (risk ratio: 1.00; 95%CI, 0.45–2.21) (3). An ongoing effort is pursuing this by pooling data across eight outpatient randomized trials.
In response to Bhattacharyya, the data are underwhelming regarding whether folic acid has activity against SARS-CoV-2 in humans to prevent or mitigate COVID-19. In-silica studies, while interesting, are low quality evidence. In pregnant women, Acosta-Elias reported a 0.95-fold risk of COVID-19-related hospitalization, which is decreased relative to influenza (4), yet CDC reported pregnant women were 2-3 fold more likely to require intensive care unit stay, invasive ventilation support, or extracorporeal membrane oxygenation (5), despite being a population commonly taking prenatal folate supplementation. The referenced 50 person case-control study is of a different population of hospitalized COVID-19 which utilized a substantially higher 150mg total dose of folic acid versus 7.6mg given in our trial (6). In our trial when comparing symptom severity by placebo composition, the mean (+SD) visual analog score did not differ at day 5 (folic acid 2.1 +2.5 vs. 2.5 +2.7 lactose; P=0.51) nor at days 10 (P=0.27) or 14 (P=0.76). Further, Mitja and colleagues, who used no placebo, reported similar overall results (2). As the available data currently stands, we feel our placebo remains valid. Effective early outpatient therapy to prevent disease progression is important, and of repurposed oral medicines, fluvoxamine appears more promising than hydroxychloroquine or folic acid (7).
References:
Scientific concerns
Without implying fabrication, several “serious scientific questions”1 on the Surgisphere study also apply to this study, rendering it uninterpretable.
Methodology, analysis, data integrity concerns
This “Post-exposure Early Treatment” (PET) study reports subjects who were symptomatic before drug receipt. Under the same protocol (NCT04308668), an asymptomatic “Post-Exposure Prophylaxis” (PEP) cohort was separately published.2
Although in both cohorts, drug was reportedly shipped to subjects overnight, our PEP dataset re-analysis3 revealed that 52% of subjects received drug 1 or 2 days later. Obtaining from the authors data that included actual shipping times, we found a 42% Covid-19 reduction associated with early (< 3 days) receipt of hydroxychloroquine (RR 0.58, 95%CI 0.35 - 0.97; p=0.044).
Sharing protocol and logistics with the PEP cohort, a similar problem in this PET cohort is reasonably suspected. With overnight shipping to subjects with < 4 days of symptoms, critically timed treatment was expected < 5 days after onset. Some subjects may have received drug 1 or 2 days later, violating the protocol, oppugning the overall analysis, and controverting a primary a priori subgroup “days of symptoms before enrollment” (Fig 5, Table S6).
Obtaining this dataset (covidpep.umn.edu/data), we have repeatedly requested actual shipping times. In extensive correspondence (osf.io/udx28/), the authors have not disputed our suspicions.
Substandard dataset prevents replication of analysis
Lack of transparency, refusal to clarify
Similar to the issue cited by the Surgisphere retraction,4 we have been unable to fully review the PET dataset or replicate its analyses. Our requests for clarification have been unanswered, although a dataset revision corrected some minor issues. Despite numerous requests, this dataset was provided some three months after the Data Sharing commitment. The journal editors advised submitting this comment.
Authors' Response
The protocol and statistical analysis plan were provided to the Annals of Internal Medicine with manuscript submission. These have been available since June 24, 2020 at https://clinicaltrials.gov/ct2/show/NCT04308668
Authors' Response to Wiseman
The protocol and statistical analysis plan were provided to the Annals of Internal Medicine at time of manuscript submission. These have also been available online since June 24, 2020 at https://clinicaltrials.gov/ct2/show/NCT04308668.
We have provided a de-identified public use dataset of the published clinical trial data which is available open-access upon completing a request at www.covidpep.umn.edu/data. Requests for potentially identifiable protected health information, such as exact dates and times, which is protected by Health Insurance Portability and Accountability Act of 1996 (HIPAA) and/or Canadian Personal Information Protection and Electronic Documents Act (PIPEDA), must be denied. Polite, professional requests for further unpublished information from multiple investigators have been generally accommodated, and the dataset and data dictionary have been updated several times since initial release to enhance clarity. With collegial interactions, we have also assisted other researchers to understand the dataset, and colleagues’ feedback has been incorporated to improve the data dictionary. All persons requesting datasets are provided the uniform resource locator (URL) to access the most updated datasets and data dictionaries. The International Committee of Medical Journal Editors (ICJME) policy does not require unpublished data to be released, nor does ICJME require the provision of free PhD biostatistician time to fulfill requests for unpublished data or analyses. All analyses published in the manuscript can be replicated from the public de-identified dataset (1).
We have sought to be entirely transparent with how our trials were conducted, including answering politely asked questions and sharing our experience with others. Additionally, we have published supplemental data in peer-reviewed journals on the logistics of how our trials operated (2). We have published the time from trial enrollment to drug delivery with a graphical representation of the data for maximal transparency (2). As these were internet-based trials (1, 3), two-thirds of participants (875/1312) enrolled outside of typical weekday, business hours. The convenience of enrolling from home during non-business hours likely enabled rapid enrollment. Thus, the overall median time from enrollment (i.e. time of informed consent) to drug delivery was 36 hours (IQR, 23.7 to 42.4). Operationally, this equates to a median participant enrollment time of 10:30pm CDT whereby the next morning, the investigational pharmacy randomized participants and dispensed study medicines up until ~4pm Monday through Friday (and until ~3pm on Saturday). Thereafter, medicines were sent by courier overnight arriving before 10:30am Monday-Saturday. Federal Express does not deliver on Sunday. In Canada, the study pharmacies dispensed on Sunday, and Purolator delivered on Sunday. We have provided shipping times in our open-access datasets for >6 months.
Regarding nomenclature of symptom duration prior to enrollment. Persons who enrolled while asymptomatic but who became symptomatic by time of receipt of study medicine were classified as having <1 day of symptoms at time of enrollment. Those enrolling on the same day that their symptoms began were categorized as having symptoms for 1 day. While some might categorize that as 0 calendar days, we categorized this as 1 day of symptoms. The overall mean (+SD) days of symptoms prior to study drug receipt was 2.7 days +2.0 days with median 3 days (IQR 1 to 4 days) in our early treatment trial (1).
In our prior postexposure prophylaxis trial (3), we have also published the effect of time from high risk exposure and time from last exposure to study drug initiation (4). With visual representation of the data, there is no conclusive effect on incidence of Covid-19 infection by timing of when hydroxychloroquine was initiated nor any statistical difference (4). The total time from reported high-risk exposure to study medicine receipt was a median of 3 days (IQR, 2 to 4) in the postexposure prophylaxis trial (2).
Unfortunately, we have learned that some persons have altered the data from our provided public dataset in their unpublished, non-peer reviewed post-hoc analyses. This is unfortunate and unnecessary. Even without altering data, we are precisely cognizant of how manipulation of small subgroups can achieve a desired p-value, based on artifacts within the placebo groups. There is significant danger in the over-interpretation of such post-hoc analyses (5), in that many of these may be incorrect. Ultimately, two other postexposure prophylaxis trials have also failed to demonstrate any benefit of hydroxychloroquine for postexposure prophylaxis (6, 7) and there was no evidence of significant effect on decreasing hospitalization in the four outpatient treatment trials evaluated in a April 2021 updated network meta-analysis (8) .
Unfortunately, it appears that hydroxychloroquine is not effective for either the prevention or treatment of Covid-19. We had hoped hydroxychloroquine would have worked, but it is time to move on to other strategies with more promise.
References:
Response from the Editors
The Editors thank Dr. Boulware and colleagues for their detailed response to Dr. Wiseman’s concerns about the conduct of their clinical trial of hydroxychloroquine in non-hospitalized patients with COVID-19 (1) and his accusations that they failed to respond appropriately to his request for study information. The trial report underwent Annals’ usual rigorous peer review process and the editors found the trial to be carefully conducted as specified in the protocol and, importantly, to reflect the real world challenges of quickly delivering medication for an acute condition to non-hospitalized patients. We also note that Boulware and colleagues provided study information and data as specified in their data-sharing plan and aligned with protection of potentially identifiable protected health information. Dr. Wiseman’s comparison of the trial published in Annals to the Surgisphere observational study that was retracted because of suspected data fabrication is unjustified. Readers should not interpret this comparison as reflecting similar issues with the conduct of Boulware and colleagues’ trial. It is disturbing to learn that Boulware and colleagues have observed that their well-intentioned data sharing was followed by manipulation of the data by those who used it to conduct post-hoc analyses. We agree that, even without altering the data, post-hoc analyses of small subgroups can achieve a desired p-value, based on artifacts within the placebo group and such analyses should be interpreted with substantial caution. While effective interventions to prevent and treat COVID-19 are sorely needed, there is substantial evidence that hydroxychloroquine is unfortunately not such an intervention.